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Bias in studies of prenatal exposures using real-world data due to pregnancy identification method

T0 review · 1 major / 6 minor · reviewed 2026-08-16 · deepseek-v4-flash

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Pith's one-line read The way researchers identify pregnancies in healthcare data can bias estimates of prenatal drug effects; the bias is only removable when missing outcomes are caused by measured variables.

desk verdict A transparent, well-benchmarked simulation showing that outcome-based pregnancy identification biases effect estimates and that the prenatal approach only fixes the problem when missingness is explained by measured covariates; the cleanest unbiasedness result is conditional on an idealized probability-1 prenatal encounter at 9 weeks. read the letter →

arxiv 2504.12415 v1 pith:ZZ4LT5HQ submitted 2025-04-16 stat.AP

Chase D. Latour , Jessie K. Edwards , Michele Jonsson Funk , Elizabeth A. Suarez , Kim Boggess , Mollie E. Wood This is my paper · ORCID
classification stat.AP MSC 62P1062D20
keywords pregnancyidentificationselectionbiasmissingnotatrandomprenatalexposuremiscarriagepharmacoepidemiologycompetingeventsdata
verification ladder T0 review T1 audit T2 compute T3 formal

The pith

A machine-rendered reading of the paper's core claim, the machinery that carries it, and where it could break.

The reading

This paper asks whether the way researchers find pregnancies in insurance claims and electronic health records—by looking for a recorded outcome like a delivery, versus by looking for a first prenatal visit—changes what they learn about prenatal medication effects. Using 10 million simulated pregnancies, it claims that when missing pregnancy outcomes are caused by unobserved miscarriage (missing not at random), the two strategies produce similarly biased risk differences and risk ratios. It claims further that the prenatal approach, which includes pregnancies whose outcomes are never observed, removes the bias only when the reasons outcomes are missing are measured variables that can be adjusted for. The practical message is that switching from outcome-based to prenatal pregnancy identification is not a cure for selection bias, but it is what makes sensible corrections possible for measurable missingness and makes the remaining bias quantifiable through sensitivity analyses.

What carries the argument

The machinery is the contrast between two cohort-construction designs: an outcome-based design that conditions on $S=1$ (observed outcome) and a prenatal design that enrolls all pregnancies at a first encounter and treats unobserved outcomes as missing data. Missingness is classified by the standard MCAR/MAR/MNAR trichotomy, and the analysis of observed pregnancies uses an Aalen-Johansen estimator within severity-rurality strata, treating miscarriage and non-preeclamptic live birth as competing events, then directly standardizes to the joint covariate distribution to estimate total effects. The load-bearing identity is that standardization can reweight the observed-pregnancies cohort only when the missingness mechanism is MAR; under MNAR, no reweighting recovers the target population, and a nonparametric bounds calculation over all possible outcomes of censored pregnancies is used to display the full range of possible effects.

What would settle it

Analyze a real claims or electronic health record database linked to a complete pregnancy registry that records miscarriages and deliveries for the same source population, estimate a prenatal drug effect three ways (observed deliveries, observed outcomes, observed pregnancies with standardization), and check whether the observed-pregnancies estimate becomes unbiased when all measured predictors of missingness are adjusted for; if it remains biased, the central claim is falsified. A cheaper check is analytic: modify the simulation so first prenatal visits occur at varying gestational ages rather than exactly 9 weeks and see whether the prenatal approach still gives unbiased estimates under MAR.

Watch

Extended reading notes

Core claim

The central claim is that the outcome-based approach to pregnancy identification—building a cohort from observed deliveries or observed outcomes—conditions on a post-exposure event ($S=1$) and cannot generally be repaired by analysis, whereas the prenatal approach reframes the problem as missing outcome data that can sometimes be fixed. In simulations where all missingness came from unobserved miscarriage, the three analytic samples (observed deliveries, observed outcomes, and observed pregnancies) all overestimated absolute risks and returned comparably biased risk differences (RDs) and risk ratios (RRs); at 20% missingness, log-transformed RR bias ranged from -0.12 to 0.33 for observed deliveries, -0.11 to 0.32 for observed outcomes, and -0.11 to 0.32 for observed pregnancies. When all missingness was due to measured covariates (hypertension severity and rurality), only the observed-pregnancies sample using standardization was unbiased, with log-RR bias from -0.02 to 0.01, while delivery-restricted and outcome-restricted samples remained biased. The paper therefore concludes that including pregnancies with unobserved outcomes does not by itself prevent bias, but it converts an intractable selection problem into a missing-data problem for which weighting, bounds, and sensitivity analyses are available.

Load-bearing premise

The load-bearing simplification is that every pregnancy has a first prenatal encounter at exactly 9 weeks, so the prenatal cohort captures the entire target population at a common time zero; if real-world first-visit timing varies or some pregnancies are never seen prenatally, the prenatal approach may no longer identify the full target population and the advantage shown here may not hold.

Editorial extensions

If this is right

  • Studies of early-pregnancy exposures (before 13 weeks) should expect some bias whenever exposure changes miscarriage risk or shares causes with miscarriage; sensitivity analyses, not cohort restriction, are needed.
  • Restricting to observed deliveries, a common default, is not a remedy and in these simulations was often the most biased sample.
  • When missing outcomes are attributable to measured factors, a prenatal cohort plus inverse-probability weighting or standardization can recover unbiased total effects; this is unavailable to outcome-based cohorts because the missing pregnancies were never identified.
  • Including pregnancies with unobserved outcomes gives investigators the extent of missingness, enabling nonparametric bounds that contained the true RD and RR in all simulated scenarios.
  • If treatment affects neither miscarriage nor preeclampsia, all identification strategies return unbiased effect estimates in the scenarios studied.

Reading between the lines

Editorial extensions of the paper, not claims the author makes directly.

  • If the simulation's idealization is relaxed so that first prenatal visits occur at varying gestational ages rather than exactly 9 weeks, the prenatal approach could inherit immortal-time or selection problems that the current setup excludes; this is a testable extension of the same simulation.
  • The same missing-data logic should transfer to other pregnancy outcomes with outcome-dependent ascertainment, such as birth defects diagnosed only after live birth, although the bias magnitudes will differ.
  • In real claims data, the 'all pregnancies' cohort may itself be incomplete because some pregnancies end before any prenatal claim appears, so the advantage shown here likely represents an upper bound unless linkage or multiple data sources capture those early losses.
  • The framing suggests that published outcome-based pharmacoepidemiology studies could be systematically re-analyzed after re-identifying pregnancies prenatally, to check whether effect estimates move in the directions predicted here.
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Editorial analysis

A structured set of objections, weighed in public.

Desk editor's note, referee report, and a circularity audit.

Referee Report

1 major / 6 minor

Summary. The manuscript studies bias in estimates of prenatal treatment effects arising from how pregnancies are identified in real-world healthcare data. Using a simulation of 10,000,000 pregnancies under a hypothetical trial of antihypertensive initiation, the authors generate potential outcomes for preeclampsia and miscarriage, induce missingness under MAR (due to measured severity/rurality), MNAR (due to unobserved miscarriage), and mixtures, and construct three analytic samples: observed deliveries, observed outcomes, and all observed pregnancies (the prenatal approach). Treatment effects are estimated by nonparametric direct standardization, or by Aalen-Johansen estimation for the all-pregnancies sample, and bias is computed against true values from the simulated potential outcomes. The central findings are that under pure MNAR all three analytic samples are similarly biased, whereas under pure MAR only the all-pregnancies sample recovers unbiased absolute risks and effect estimates; the observed deliveries and observed outcomes samples remain biased. The paper frames outcome-based pregnancy identification as selection bias and the prenatal approach as a missing-data problem, and argues the prenatal approach enables sensitivity analyses and bounds.

Significance. If the results hold, the paper fills a genuine gap: prior work has focused on conditioning on live birth, but not on the bias induced by the pregnancy identification strategy itself. The simulation is carefully constructed, large, and checked against known true values from potential outcomes rather than fitted to a target, and the code is publicly available. The comparison of observed deliveries versus observed outcomes versus all pregnancies under MAR/MNAR gives a concrete, useful message for pharmacoepidemiology: outcome-based identification cannot generally be fixed by analytic methods, while the prenatal approach only removes bias when missingness is explained by measured covariates. The paper also contributes a clear DAG-based taxonomy and demonstrates full sensitivity bounds for the prenatal approach. These strengths make the study a solid methodological contribution, provided the central assumption discussed below is either relaxed in additional simulations or its conditioning role is stated more sharply.

major comments (1)
  1. [Methods S6 and Discussion, Limitations] The central quantitative comparison is conditional on the assumption, stated in Methods S6, that every pregnancy has a prenatal encounter with probability 1 at exactly 9 weeks gestation. This guarantees that the 'observed pregnancies' analytic sample is the full target population at a common time zero, so unbiasedness under 100% MAR follows from correct specification of the censoring model within severity-rurality strata. If first-encounter timing varies or some pregnancies are never captured by a prenatal visit, the observed-pregnancies sample is itself selected and standardization to its covariate distribution will not recover the target-population effect even under MAR. The manuscript acknowledges this limitation but does not quantify how the relative performance of the three approaches changes when the probability-1 common-time-zero assumption fails. Because the paper's practical message ('only among all pregnancies did bias decrease as the proportion of missingness due to measured variables increased') depends on this assumption, I ask the authors to add a simulation arm that varies first-encounter timing or capture probability, or to explicitly and prominently restrict the conclusion to the idealized setting and state that the ordering of approaches is not established when capture is incomplete.
minor comments (6)
  1. [Figure 5 caption] The caption labels the fourth panel '(D) MAR', but panels are already labeled (A), (B), (C), (D) for MNAR, mixed, and MAR in the main text; this should read '(F) MAR' to match the corresponding panels in Figure 4 and the text.
  2. [Table S10] In the final block of Table S10 ('Initiation increases the risk of abortion and does not affect the risk of preeclampsia'), the numbers of pregnancies in the target population appear to be about 2.5 million per arm rather than the 5 million per arm used in all other scenarios; this is inconsistent with the stated 10 million pregnancies and should be corrected or explained.
  3. [Tables S4-S10] The supplemental tables use the term 'abortion' where the main text uses 'miscarriage'; the terminology should be harmonized to avoid confusion, since 'abortion' has a different clinical meaning.
  4. [Methods S10] The rationale for assigning a follow-up time of 0.0001 to pregnancies with only the initial prenatal encounter should be stated more explicitly; this effectively censors those pregnancies at baseline, and the text should say so and note that the results are insensitive to the choice of this small constant.
  5. [Data and Code Availability] The main-text statement 'All code is available on GitHub ([LINK TO FOLLOW UNBLINDING])' contains a placeholder; the actual repository URL appears in the front matter and should be inserted in the body of the manuscript.
  6. [Figure S8 panel headers] The third panel of Figure S8 labels the scenario 'All MNAR: 100% Severity, 0% Miscarriage'; since this panel represents all missingness due to measured severity/rurality, it should be labeled 'All MAR' to match the other figures.

Circularity Check

0 steps flagged · score 0.0 of 10

No circularity: simulation findings are internal validations against known potential outcomes, not fitted predictions.

full rationale

The paper's central claims are derived by simulating a target population with known potential outcomes, inducing missingness under explicit mechanisms, and comparing each analytic sample's standardized estimates to the true simulated values. Bias is therefore measured against an external ground truth generated from the simulation, not fitted to a target answer. The result that the observed-pregnancies sample is unbiased when all missingness is due to measured covariates follows from the data-generating mechanism (Methods S7-S9 make missingness depend only on severity and rurality) together with the standardization estimator described in Methods S10, which the paper explicitly notes is appropriate because censoring is random within strata of severity. This is an internal consistency check, not a circular prediction: the same construction also yields the non-tautological comparative findings, e.g., that all three samples are similarly biased under MNAR due to unobserved miscarriage and that observed deliveries are often the most biased. The paper itself frames the simulation as illustrating theoretical expectations rather than deriving a first-principles result from its own conclusions. Self-citations (e.g., reference 35 on competing events and reference 49 on target-trial emulation) are used for standard methods and are not load-bearing; the relevant estimators are described in the supplement. The idealized assumption of a probability-1 prenatal encounter at exactly 9 weeks is an acknowledged limitation affecting external validity, not a circular step, because it does not smuggle the conclusion into the analysis; it is a stated simplification of real-world data structure. No specific circular step meeting the quoted-equation standard was found.

Assumptions & free parameters 5 free parameters · 6 assumptions · 0 invented entities

The central claims are conditional on a fully specified simulation. The listed free parameters are not fitted to the study's target estimates, but they are hand-chosen inputs that set the bias magnitudes; the axioms are the structural assumptions that make the simulation tractable and the prenatal-approach estimator valid. The paper itself flags the simplification to universal 9-week initiation and the absence of induced abortion.

free parameters (5)
  • Treatment effect on miscarriage risk (weekly RR multipliers) = Decrease: 0.1, 0.5, 0.8 by severity; Increase: 5, 2, 1.1; None: 1
    Manually selected scenario values (Methods S2) that determine true risks and bias magnitudes in the six target populations.
  • Treatment effect on preeclampsia (weekly OR multipliers) = Decrease: ln(0.2), ln(0.5), ln(0.8); None: ln(1)
    Scenario values (Methods S3) used to induce effects of antihypertensive initiation on preeclampsia.
  • Covariate-outcome association parameters = Fetal death: severity RR 2 and 3, rural RR 1.5; preeclampsia: severity OR 1.5 and 2, rural OR 2; preeclampsia fetal…
    Fixed by hand to approximate published epidemiology (Methods S2-S4); these associations determine how well measured covariates predict both outcome and missingness.
  • Missingness model coefficients = alpha1 and alpha2 for severity/rurality; delta1 for gestational age at miscarriage; balancing intercepts in Table S3
    Chosen to hit target missingness percentages (5% or 20%) and MAR/MNAR splits (Methods S8-S9); these define the mechanisms being compared.
  • Target missingness fractions = 5% or 20%; 0/50/100% due to measured variables
    Scenario design choices; the paper reports larger bias at 20% missingness.
assumptions (6)
  • domain assumption All pregnancies have a prenatal care encounter at exactly 9 weeks gestation with probability 1 (Methods S6).
    Guarantees the prenatal approach identifies every pregnancy at a common time zero; real-world encounter timing varies, which the authors acknowledge in Limitations.
  • domain assumption Perfect treatment persistence: initiators are always treated after the index encounter and non-initiators never are (Methods S5).
    Eliminates time-varying exposure and immortal time; real data require target trial emulation, as the authors note.
  • domain assumption No induced abortions or pregnancy terminations occur in the target population (Discussion).
    Restricts missingness sources to miscarriage and measured variables; induced abortion could add MNAR missingness.
  • domain assumption Gestational age is measured without error, so the target population at 9 weeks is correctly identified (Limitations).
    Real claims data have gestational age uncertainty that can misclassify pregnancy timing.
  • domain assumption Within strata of measured covariates, censoring is independent of preeclampsia risk (Methods S10).
    This is what makes the Aalen-Johansen estimator unbiased in the observed-pregnancies sample; it holds by construction in the simulation under MAR.
  • domain assumption Preeclampsia causes the pregnancy outcome within one week deterministically (Methods S4).
    Simplifies competing event timing; the authors state that timing does not affect the study's results.

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Pith. "Pith review of Bias in studies of prenatal exposures using real-world data due to pregnancy identification method." pith.science (2026). https://pith.science/paper/ZZ4LT5HQ

@misc{pith2026250412415,
  author       = {Pith},
  title        = {Pith review of: Bias in studies of prenatal exposures using real-world data due to pregnancy identification method},
  year         = {2026},
  howpublished = {\url{https://pith.science/paper/ZZ4LT5HQ}},
  note         = {Machine review of arXiv:2504.12415}
}
read the original abstract

Background: Researchers typically identify pregnancies in healthcare data based on observed outcomes (e.g., delivery). This outcome-based approach misses pregnancies that received prenatal care but whose outcomes were not recorded (e.g., at-home miscarriage), potentially inducing selection bias in effect estimates for prenatal exposures. Alternatively, prenatal encounters can be used to identify pregnancies, including those with unobserved outcomes. However, this prenatal approach requires methods to address missing data. Methods: We simulated 10,000,000 pregnancies and estimated the total effect of initiating treatment on the risk of preeclampsia. We generated data for 36 scenarios in which we varied the effect of treatment on miscarriage and/or preeclampsia; the percentage with missing outcomes (5% or 20%); and the cause of missingness: (1) measured covariates, (2) unobserved miscarriage, and (3) a mix of both. We then created three analytic samples to address missing pregnancy outcomes: observed deliveries, observed deliveries and miscarriages, and all pregnancies. Treatment effects were estimated using non-parametric direct standardization. Results: Risk differences (RDs) and risk ratios (RRs) from the three analytic samples were similarly biased when all missingness was due to unobserved miscarriage (log-transformed RR bias range: -0.12-0.33 among observed deliveries; -0.11-0.32 among observed deliveries and miscarriages; and -0.11-0.32 among all pregnancies). When predictors of missingness were measured, only the all pregnancies approach was unbiased (-0.27-0.33; -0.29-0.03; and -0.02-0.01, respectively). Conclusions: When all missingness was due to miscarriage, the analytic samples returned similar effect estimates. Only among all pregnancies did bias decrease as the proportion of missingness due to measured variables increased.

Figures

Figures reproduced from arXiv: 2504.12415 by the authors.

Figure 1
Figure 1. Directed acyclic graphs for a study assessing the effect of a prenatal exposure E on multinomial study outcome D(j) with risk factor C and indicator for missing pregnancy outcome S. A box around S = 1 indicates that only individuals with an observed pregnancy outcome are included in the analytic cohort. E D( j ) C (A) S=1 E D( j ) C (B) S=1 E D( j ) C (C) S=1 [PITH_FULL_IMAGE:figures/full_fig_p026_1.png] view at source ↗

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Pith tools

Reviewed August 16, 2026 · model on record in the stance chip above.